A Study of Participant Preference With Subcutaneous Versus Intravenous MabThera/Rituxan in Participants With CD20+ Diffuse Large B-Cell Lymphoma or CD20+ Follicular Non-Hodgkin's Lymphoma Grades 1, 2 or 3a: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study of Participant Preference With Subcutaneous Versus Intravenous MabThera/Rituxan in Participants With CD20+ Diffuse Large B-Cell Lymphoma or CD20+ Follicular Non-Hodgkin's Lymphoma Grades 1, 2 or 3a (NCT01724021), a randomized phase 3 study. The primary outcome is Percentage of Participants Indicating a Preference for Rituximab Subcutaneous (SC) Over Rituximab Intravenously (IV) at Cycle 6.

2. Clinical Question

3. Trial Design

This Phase 3 study was randomized, open-label, multicentre, and used a parallel-group design. The registry records enrollment of 743 participants and a completed study. It lists the study start as 2012-12 and primary completion as 2015-01. The sponsor was Hoffmann-La Roche.

The arms differed in when participants received each route of rituximab. Arm A received one cycle of intravenous rituximab, three cycles of subcutaneous rituximab, then four cycles of intravenous rituximab. Arm B received four cycles intravenously followed by four cycles subcutaneously. The brief description specifies intravenous rituximab at 375 mg/m2 and subcutaneous rituximab at 1400 mg. Both arms received 6–8 cycles of standard chemotherapy alongside 8 cycles of rituximab. Chemotherapy options listed in the registry were CHOP, CVP, or bendamustine, according to local practice. Anticipated time on study treatment was up to 24 weeks.

Because the study was open-label, participants and study personnel were not masked to the administration route. That is relevant to a preference outcome: participants knew which route they received when giving their response. The primary endpoint was assessed after Cycle 6, when the two arms had different treatment sequences and exposure to the routes. The registry does not report a protocol for how participants were assigned to chemotherapy choices or how these choices were handled in the statistical analysis.

The posted primary endpoint results include 372 evaluable participants in Arm A and 371 in Arm B. The endpoint description defines the intention-to-treat population as all randomized participants, while also noting that the number analyzed is the number evaluable for the outcome. Reasons for any difference between randomized and evaluable numbers are not reported in the registry record. The registry lists 14 outcome measures and 12 posted secondary outcomes. Detailed numeric results are available for the primary endpoint and the complete response rate; analyses for other secondary outcomes are not reported in the registry record.

4. Participant Flow and Accounting

The registry reports how participants moved through each stage of the study. All counts below are exactly as posted; missing counts are not inferred from other stages.

Before assignment: A total of 743 participants were enrolled across all the sites and were included in the intent to treat (ITT) population. Three participants were enrolled but died prior to receiving study medication and were not included in the safety population. The Participant Flow represents the safety population.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: ITT population included all participants who were randomized in the study. Number of participants analyzed specifies number of participants who were evaluable for the outcome measure.

5. Baseline Characteristics

The table reproduces the baseline characteristics posted in the registry, which describe the participants analysed at baseline and help show whether the randomized groups were comparable.

6. Primary Endpoint

The registry lists the primary outcome as Percentage of Participants Indicating a Preference for Rituximab Subcutaneous (SC) Over Rituximab Intravenously (IV) at Cycle 6, measured over Cycle 6 (Up to 24 weeks).

The primary endpoint is the percentage of participants indicating a preference for subcutaneous rituximab over intravenous rituximab after completing Cycle 6. It was assessed using the patient preference questionnaire, with results reported separately for Arm A and Arm B and accompanied by 95% confidence intervals. The timeframe is Cycle 6, up to 24 weeks.

This endpoint addresses participants’ stated preference between two ways of administering the same drug within treatment schedules that differed by arm. It does not measure preference for rituximab versus another medicine, nor does it directly measure disease control or survival. A preference response is a participant-reported outcome: it captures an expressed choice at the specified assessment, not an objective measure of treatment efficacy. The open-label design is particularly relevant because participants knew the administration route they had received.

The registry describes the intention-to-treat population as all randomized participants, but says that the number analyzed specifies those evaluable for the outcome. Thus the posted percentages should be read alongside the evaluable numbers and their confidence intervals. How unevaluable responses were handled, and whether the analysis used any adjustment beyond the reported endpoint calculation, are not reported in the registry record.

7. Results Posted in the Registry

• Arm B: 80.6% (299/371) versus 79.0% (294/372) on control; risk difference 1.6 percentage points (95% CI -4.2 to 7.3), risk ratio 1.02 (0.95–1.10); unadjusted two-proportion z-test p = 0.596.

8. Secondary Efficacy Endpoints

The registry also posts results for secondary outcomes. For each outcome below, the endpoint type, the test applied to the posted summary statistics, the result and its interpretation are given in turn. Secondary endpoints are usually not adjusted for multiple testing, so they support rather than confirm the primary finding.

Complete Response (CR) Rate

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Arm B: 52.7% (166/315) versus 49.2% (151/307) on control; risk difference 3.5 percentage points (95% CI -4.3 to 11.4), risk ratio 1.07 (0.92–1.25); unadjusted two-proportion z-test p = 0.381.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Arm B and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes span several distinct questions: treatment-emergent adverse events, time required for each administration route, satisfaction questionnaires, complete response, and event-free, disease-free, and progression-free survival. These outcomes do not all measure the same construct. Preference and satisfaction are participant-reported experiences; response and survival endpoints concern disease outcomes; adverse events address safety; and administration time concerns treatment delivery. They can add context to the primary preference result but should not be combined into a single overall judgment.

The posted complete response results offer a separate disease-response perspective. The arm percentages and unadjusted comparison have uncertainty that includes no difference, and the outcome uses a different assessment time and analysis population from the primary endpoint. It neither measures preference nor directly explains why a participant chose a route. The results for the other listed secondary outcomes are not reported in the registry record, so their direction, size, and precision cannot be assessed from the available record.

Unadjusted secondary results generally carry less weight than a prespecified primary analysis because many outcomes can be examined, increasing the chance that at least one appears notable by chance. This concern is especially relevant when several endpoints, timeframes, or analyses are considered. The registry does not report a multiplicity procedure, a hierarchy of secondary hypotheses, or sponsor-reported analyses for the posted secondary result. Consequently, the complete response comparison should be treated as descriptive and exploratory rather than as a confirmatory finding. The other listed outcomes should not be assumed to support or contradict the primary result in the absence of posted numerical results.

Secondary outcomes registered for this trial, for reference (only those above were recalculated):

• Number of Participants With Treatment Emergent Adverse Events (AEs)
• Time Required for Rituximab Administration (Subcutaneous [SC] or Intravenous [IV])
• Cancer Therapy Satisfaction Questionnaire (CTSQ) Score
• Rituximab Administration Satisfaction Questionnaire (RASQ) Score
• Complete Response (CR) Rate
• Event-free Survival (EFS)
• Disease-free Survival (DFS)
• Progression-free Survival (PFS)

9. Statistical Interpretation

10. Statistical Methods Explained

What does a percentage with a confidence interval describe?

The primary outcome is binary at the participant level: a participant either indicated a preference for subcutaneous over intravenous administration or did not. The percentage is the observed proportion of evaluable participants in an arm who indicated that preference. The accompanying 95% confidence interval expresses uncertainty about the underlying proportion that could have generated the observed data under the assumptions of the interval method. A narrower interval indicates greater precision; a wider interval indicates more uncertainty. The specific method used to calculate the registry’s arm-level intervals is not reported in the registry record.

How should the between-arm difference be read?

A risk difference subtracts one arm’s event proportion from the other arm’s event proportion. Here, the posted comparison is for Arm B versus Arm A and is 0.016. The reported 95% confidence interval runs from -0.042 to 0.073. A value of zero would represent equal proportions. Because this interval includes zero, it does not rule out no difference at the level of uncertainty represented by that interval. It also includes values on both sides of zero, so the direction of a possible difference is uncertain. The comparison is an unadjusted calculation from posted summary counts, not a reported adjusted model.

What does the p-value contribute?

The unadjusted p-value of 0.596 summarizes how surprising data at least this inconsistent with an equal-proportion assumption would be if that assumption and the test’s other assumptions held. It is not the probability that the arms are equal, nor a measure of the size or practical importance of a difference. A p-value does not replace the estimate and confidence interval: the estimate describes the observed contrast, and the interval describes its uncertainty. The registry does not report the sponsor’s testing method or a sponsor-reported comparison for the primary endpoint.

Why does the design matter for a preference outcome?

Random assignment creates a basis for comparing the two treatment sequences, but the open-label design means participants knew their administration route. Knowledge and experience can be relevant to a reported preference. In addition, the schedules deliberately differed in when subcutaneous and intravenous administrations occurred. A comparison between arms is therefore a comparison of sequences at the Cycle 6 assessment, not a randomized comparison in which only the route at that moment necessarily differed. The registry does not report an analysis separating the contribution of sequence, prior experience, or other influences on preference.

What do the analysis populations tell readers?

The endpoint description defines the intention-to-treat population as everyone randomized, while clarifying that the number analyzed is the number evaluable for the outcome. The displayed endpoint denominators are 372 and 371. This distinction matters because a randomized participant without an evaluable questionnaire response may not contribute to the displayed percentage. The registry does not report the number or reasons for missing or unevaluable responses, nor whether missing responses were imputed or handled in another way.

What is known about the statistical plan?

The registry reports the endpoint definition, its timeframe, arm-level estimates, and confidence intervals. It does not report the original trial sample-size justification, the exact method for calculating the endpoint confidence intervals, an adjusted primary analysis, interim analyses, or a multiplicity procedure. Those details cannot be inferred from the posted estimates. The planning illustration displayed with the results is a separate calculation using the observed effect and stated assumptions; it is not evidence about the trial’s original design plan.

Why might over-dispersion matter in other settings?

As a general statistical concept, over-dispersion occurs when variation in data is greater than a model assumes. In a binary-outcome analysis, unaccounted-for clustering or other dependence can make uncertainty estimates too optimistic. The registry describes a multicentre study but does not report whether the primary analysis adjusted for centre or any other clustering. There is no basis in the registry record to say that over-dispersion occurred in this study; the concept is relevant only as a general consideration when interpreting the assumptions behind an analysis.

The complete response result is also binary, but its evaluable denominators differ from those for the primary endpoint. Its unadjusted comparison is a separate calculation, and the registry does not report a sponsor analysis for it. A confidence interval for a secondary endpoint communicates uncertainty about that endpoint’s estimate, but it does not account for the fact that multiple outcomes were assessed. That issue is important when considering how much weight to give a collection of secondary findings.

11. Confidence Intervals and Precision

The primary arm-specific confidence intervals are 74.2% to 83.5% for Arm A and 75.7% to 84.8% for Arm B. Each interval is several percentage points wide, so the point estimates should not be treated as exact values for a broader population. Both intervals cover a range of plausible preference proportions under the assumptions of the interval method. Their overlap is substantial, which is consistent with the small estimated difference between arms, though overlap of separate arm intervals is not itself the formal test of an arm difference.

The direct unadjusted comparison is more useful for describing uncertainty about the contrast. Its estimated risk difference is 0.016, and its 95% confidence interval extends from -0.042 to 0.073. Since the interval includes zero and allows estimates on both sides of zero, the posted comparison does not precisely establish the direction of a between-arm difference. The unadjusted p-value of 0.596 is consistent with that uncertainty, but it does not quantify the probability that the null hypothesis is true.

The confidence intervals describe sampling uncertainty under the analysis assumptions; they do not capture every possible source of uncertainty. They cannot correct for missing questionnaire responses, open-label influences on stated preference, or limitations in the outcome’s definition. The reasons participants were not evaluable and the precise interval calculation method are not reported in the registry record. Precision should therefore be considered alongside the design and reporting limitations, not as a complete measure of the study’s reliability.

12. Planning a Similar Trial: Sample Size

This is a planning illustration, not a re-evaluation of the original trial. It asks: if a new study wanted to detect a difference like the one observed, or a smaller one, how large would it need to be? It is deliberately not “observed power” of the finished trial, which is not a meaningful quantity.

The planning figures are participants per arm for the binary outcomes, rather than total events. The registry’s planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set to the stated fraction of the observed effect. The original trial’s own sample-size assumptions and justification are not reported in the registry record.

The 80% power column gives the illustrative number of participants per arm under which a design would have an 80% chance of detecting the specified effect if the planning assumptions held. The 90% power column describes the corresponding chance as 90%. These are planning calculations for hypothetical future designs, not a description of the chance that this completed study found a result. This is not observed power.

Rows planning for 100%, 75%, and 50% of the observed effect represent progressively smaller effects to detect. Smaller effects generally require more participants to distinguish them from random variation under the same planning assumptions. For the primary endpoint, the illustrative figures range from 10,383 participants per arm for 80% power and 13,899 for 90% power when planning for 100% of the observed effect, to 42,128 and 56,397 when planning for 50% of the observed effect. The 75% row gives 18,591 and 24,888 participants per arm. These are not enrollment targets for the completed study; they are scenario-based planning illustrations.

The complete response planning illustration uses its own observed effect and gives different figures: 3,179 participants per arm for 80% power and 4,255 for 90% power at 100% of that observed effect; planning for 75% gives 5,653 and 7,567, and planning for 50% gives 12,721 and 17,029. The registry’s general note distinguishes binary outcomes, reported as participants per arm, from time-to-event outcomes, for which planning figures would be total events. The primary and complete response illustrations are binary-outcome calculations.

13. How the Sample Size Is Derived

Power is the probability that a study of a given size rejects the null hypothesis when a specific true effect exists. It depends on four things: the effect to detect, the variability of the outcome, the significance level (here a two-sided α of 0.05, so z_1−α/2 = 1.960) and the desired power (z_1−β = 0.842 for 80% and 1.282 for 90%).

Formula

n is the number of participants in each arm, p₀ and p₁ are the control and treatment proportions, and p̄ is their average.

Worked calculation for this trial

1. Control proportion p₀ = 0.790; treatment proportion p₁ = 0.806; average p̄ = 0.798.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5677 = 1.1126.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5676 = 0.4777.
4. n = (1.1126 + 0.4777)² / (0.0156)² = 10,382.0, rounded up to 10,383 participants per arm for 80% power.

The smaller-effect rows in the table above repeat the same calculation with the effect multiplied by 0.75 and 0.5 (for ratios, applied to the logarithm of the ratio).

R code

alpha <- 0.05
z_a   <- qnorm(1 - alpha / 2)          # two-sided
p0 <- 0.790322580645161                          # control proportion
p1 <- 0.805929919137466                          # treatment proportion
n_per_arm <- function(power, frac = 1) {
  q1 <- p0 + (p1 - p0) * frac               # smaller effect = fraction of the observed difference
  pbar <- (p0 + q1) / 2
  z_b <- qnorm(power)
  ceiling(round((z_a * sqrt(2 * pbar * (1 - pbar)) + z_b * sqrt(p0 * (1 - p0) + q1 * (1 - q1)))^2 / (q1 - p0)^2, 6))
}
for (f in c(1, 0.75, 0.5))
  cat(sprintf("%3.0f%% of observed effect: n per arm = %s (80%% power), %s (90%% power)\n", 100 * f,
              format(n_per_arm(0.80, f), big.mark = ","), format(n_per_arm(0.90, f), big.mark = ",")))

# Check against R's built-in function (unrounded n per arm)
cat("power.prop.test:", round(power.prop.test(p1 = p0, p2 = p1, power = 0.80)$n, 1), "\n")

# Simulation: how often does the z-test reject at the 80%-power sample size?
set.seed(1724021)
n    <- n_per_arm(0.80)
reps <- 20000
x0 <- rbinom(reps, n, p0); x1 <- rbinom(reps, n, p1)
ph <- (x0 + x1) / (2 * n)
z  <- ((x1 - x0) / n) / sqrt(ph * (1 - ph) * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(z) > z_a, na.rm = TRUE), reps))

Output from running the code

100% of observed effect: n per arm = 10,383 (80% power), 13,899 (90% power)
 75% of observed effect: n per arm = 18,591 (80% power), 24,888 (90% power)
 50% of observed effect: n per arm = 42,128 (80% power), 56,397 (90% power)
power.prop.test: 10382 
Simulated power at n = 10,383 per arm: 0.799 (20000 replicates)

The simulation draws many pairs of event counts at the planned sample size and counts how often the two-proportion z-test rejects the null. It should land close to the target power; at very small required sample sizes it can fall below it, because the normal approximation is rough there.

14. Multiplicity, Missing Data and Analysis Populations

The registry lists multiple outcome measures, including a primary preference endpoint and secondary measures covering safety, administration time, satisfaction, response, and time-to-event outcomes. Testing or interpreting many outcomes creates a multiplicity concern: even when there is no true difference for any outcome, some observed results may appear unusual by chance. A prespecified testing hierarchy or adjustment can help control that concern, but a multiplicity plan is not reported in the registry record.

The primary comparison available in the posted results is an unadjusted calculation from summary counts. The registry does not report a sponsor-reported statistical analysis for the primary endpoint comparison, an adjusted analysis, or details of any interim analyses. It also does not report a multiplicity procedure for secondary outcomes. The unadjusted p-values for the primary and complete response comparisons should therefore not be read as if they accounted for all the outcomes assessed.

The endpoint description says the intention-to-treat population included all randomized participants, but specifies that the number analyzed was the number evaluable for the endpoint. The displayed primary denominators are 372 in Arm A and 371 in Arm B, and the complete response denominators are 307 and 315. The registry does not explain why the evaluable counts differ across outcomes, give the number of missing responses, or describe how missing data were handled. It is therefore not possible to assess from the registry record whether missingness could have affected the estimates.

These reporting gaps do not establish that the trial lacked a statistical plan or that missing data biased the results. They mean only that the relevant procedures and details are not reported in the registry record. Readers should distinguish the posted arm-level estimates and unadjusted calculations from an undocumented sponsor analysis, and avoid treating the set of secondary outcomes as a collection of confirmatory tests.

15. Safety Results

The registry reports serious adverse events as affected participants divided by participants at risk.

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: febrile neutropenia (8.4%), neutropenia (4.3%), pneumonia (3.2%), neutrophil count decreased (3.0%), pyrexia (2.7%).

For serious adverse events, the registry lists 126 affected participants among 371 at risk in Arm A and 116 among 369 at risk in Arm B. These are arm-level counts and denominators; they are not a comparison adjusted for treatment exposure or other factors. The registry also gives other adverse-event counts of 318 among 371 in Arm A and 317 among 369 in Arm B. Serious and other adverse-event categories should be read as distinct reported summaries, not added together.

The most frequently listed serious adverse event terms include febrile neutropenia at 8.4%, neutropenia at 4.3%, pneumonia at 3.2%, neutrophil count decreased at 3.0%, pyrexia at 2.7%, and anaemia at 1.4%. These term-specific figures describe the posted serious-event listings; they do not establish a causal relationship or provide a complete comparison of risk between arms. Death figures are not reported in the registry record. The registry does not provide additional detail in the posted material on event timing, duration, severity grading, or exposure-adjusted rates.

16. What the Result Does, and Does Not, Mean

The primary result describes the percentage of evaluable participants who stated a preference for subcutaneous rather than intravenous rituximab at the Cycle 6 assessment. The percentages were 79.1% in Arm A and 80.6% in Arm B. The unadjusted estimated difference is 0.016, with a 95% confidence interval that includes zero, and the unadjusted p-value is 0.596. Taken together, these results do not demonstrate a clear between-arm difference in stated preference.

That interpretation is specific to the comparison and outcome measured. Both arms received rituximab by both routes, but in different sequences, with chemotherapy given as well. The study therefore does not compare subcutaneous rituximab with no rituximab, and the arm comparison is not a test of a route used in isolation from treatment sequence. The outcome records a preference at Cycle 6; it does not establish that every participant preferred the same route at every point in treatment.

A stated preference is not a measure of tumor response, survival, or treatment safety. The separately posted complete response result is a secondary endpoint and its unadjusted interval also includes zero. Other secondary outcomes are listed, but numerical results for most are not reported in the registry record. The available registry results thus cannot support a broad conclusion about all efficacy, experience, or safety outcomes.

The open-label design is relevant because participants knew the route they received, and the registry does not describe how missing or unevaluable questionnaire responses were handled. These limitations qualify how the percentages should be generalized. They do not overturn the arithmetic of the posted estimates, but they identify factors that the confidence intervals alone do not address. No medical decision follows from these statistics alone.

17. Why This Trial Matters Statistically

This trial raises a useful statistical distinction between comparing treatments and comparing treatment experiences. Its primary question concerns participant preference for a route of administration, assessed after a sequence in which participants received both intravenous and subcutaneous rituximab. The outcome is therefore an expressed preference tied to prior experience, not a direct biological measure of treatment effect.

The randomized, parallel-group design supports a comparison of the two assigned schedules, while the open-label design is important for interpreting a participant-reported outcome. Randomization does not remove the possibility that knowledge of the route or the order of exposure influences a stated preference. The registry reports a close pair of arm-specific preference estimates and an unadjusted comparison whose confidence interval spans zero. This illustrates why the size and precision of a contrast matter alongside a p-value.

The record also illustrates the limits of reading secondary outcomes without an explicit analysis plan. Several different kinds of outcomes were listed, but only one secondary endpoint has detailed numeric results in the posted information, and no multiplicity procedure is reported. A long outcome list is not equivalent to a complete set of interpretable findings. The planning illustrations further demonstrate that sample-size calculations depend on the effect assumed for detection and should not be mistaken for a post hoc measure of study success.

Finally, the distinction between an intention-to-treat population and participants evaluable for a particular outcome is consequential. The endpoint definition refers to all randomized participants, but the reported denominators are evaluable counts. Without reasons for missing assessments and details of their handling, readers cannot fully assess the potential effect of missingness. These are general lessons in interpreting randomized studies with participant-reported endpoints and multiple outcomes.

18. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.
• Participant counts were reconstructed from posted percentages and arm sizes, so small rounding differences are possible.

Several limitations specific to this record affect interpretation. The study was open-label, and the primary endpoint was a participant-reported preference. Participants knew which route they received, so the reported response reflects preference in that setting rather than a blinded comparison. Because the arms used different sequences of intravenous and subcutaneous treatment, the Cycle 6 result may reflect the overall sequence and experience, not only the route received at the assessment.

The primary endpoint’s evaluable counts are reported, but the registry does not report the number of missing or unevaluable questionnaires, the reasons for missingness, or how missing responses were handled. The record defines the intention-to-treat population as all randomized participants while specifying that the number analyzed is the number evaluable. This leaves uncertainty about the relationship between the intended population and the displayed estimates.

The registry does not report the original sample-size justification, the confidence-interval calculation method, an adjusted primary comparison, interim analyses, or a multiplicity procedure. The posted between-arm calculation is unadjusted. The record also lists many secondary outcomes, but detailed numeric results are not reported for most of them, limiting assessment of the wider outcome pattern. Although some serious adverse event counts and event terms are available, death figures and further detail on timing, duration, and exposure-adjusted rates are not reported in the registry record.

These limitations describe what cannot be assessed from the registry record; they do not show that the underlying study procedures were inadequate. The uncertainty and scope of inference should be kept in view when interpreting the primary preference comparison and the limited secondary results.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: A Study of Participant Preference With Subcutaneous Versus Intravenous MabThera/Rituxan in Participants With CD20+ Diffuse Large B-Cell Lymphoma or CD20+ Follicular Non-Hodgkin's Lymphoma Grades 1, 2 or 3a — NCT01724021.
• Registry record last updated 2018-01-23; status last verified 2017-12.
• Results first posted 2016-08-29.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

22. Record Summary

NCT01724021 was a completed, randomized, open-label, parallel-group Phase 3 study sponsored by Hoffmann-La Roche. It enrolled 743 participants with previously untreated CD20+ diffuse large B-cell lymphoma or CD20+ follicular non-Hodgkin's lymphoma Grades 1, 2 or 3a. The arms received different sequences of intravenous and subcutaneous rituximab alongside standard chemotherapy.

The primary endpoint was preference for subcutaneous over intravenous rituximab after Cycle 6. The reported percentages were 79.1% in Arm A and 80.6% in Arm B; the unadjusted risk difference was 0.016, with a 95% confidence interval from -0.042 to 0.073 and an unadjusted p-value of 0.596. The registry also posts complete response results, while numerical results for most other listed secondary outcomes are not reported in the registry record.